Tuesday, 13 August 2013

A kingdom for a scale

The recent hiatus, so far the longest in the history of Résonaances, was caused by a unique combination of work, travel, frustration, depression, and sloth. Sorry :-|  A day may come when this blog will fall silent forever; but it is not this day ;)
 
After the first run of the LHC particle physics finds itself in an unprecedented situation. During most of  the history of the discipline we had a high energy scale that allowed us to organize our theoretical and experimental efforts. It first appeared back in the 1930s when Fermi wrote down his theory of weak interactions which contained a 4-fermion operator mediating the beta decay of the neutron. For dimensional reasons, 4-fermion operators appear in the Lagrangian divided by an energy scale squared, and in the case of the Fermi operator  this scale is what we now know as the electroweak scale v=174 GeV. This scale come with well defined physical consequences. Scattering amplitudes in the Fermi theory misbehave at energies above v, and some new physics must appear to regulate them. Later several details of this picture were modified. In particular, it was found that the Fermi  4-fermion operator is a low energy effective description of the exchange of a W boson between pairs of fermions. However the argument for new physics near the electroweak scale remained in place, this time to regulate the W and Z bosons scattering amplitudes. That's why even before the LHC kicked off  we could give an almost risk-free promise that it was going to discover something.

Now things have changed dramatically. The LHC has explored the energy range up to about 1 TeV and definitively crossed the electroweak scale. The promised new physics phenomenon was found: a spin-0 boson coupled to mass,  as predicted in the Standard Model. This little addition miraculously cures all the woes of the theory. Ignoring gravity, the Standard Model with the 125 GeV Higgs boson can be extended to arbitrarily high scales. Only the coupling of matter to gravity guarantees some new phenomena, like maybe strong gravitational effects and production of black holes. But that should happen at an immensely high scale of 10^19 GeV that we may never be able to reach in collider experiments. We are not sure if  there is any other physical scale between the electroweak and Planck scale. There's no well defined energy frontier we can head toward. Particle physics no longer has  a firm reference point. An artist's view of the current situation is this:

There's actually one important practical consequence.  Regardless how high energy collider we build next: 30 TeV, 100 TeV, or 1000 TeV,  we cannot be sure it will discover any new phenomena rather than just confirm the old theory in the new energy range. 

This is not to say that the Standard Model must be valid all the way to the Planck scale. On the contrary we have strong hints it is otherwise. The existence of dark matter, the observations of  neutrino oscillations, the matter-antimatter asymmetry in the Universe, and the cosmological inflation, they all require some physics beyond the Standard Model. However none of the above points to a concrete scale where new phenomena must show up. The answers may be just behind the corner  and be revealed by the run-II of the LHC. Or the answer may be due to Planck-scale physics and will never be directly explored; or else it may be due to very light and very weakly coupled degrees of freedom that should be probed by other means than colliders. For example, for dark matter particles we know theoretically motivated models with the mass ranging from sub-eV (axions) to the GUT scale (wimpzillas), and there is no mass  between these two extremes that is clearly favored from the theory point of view.  The case of the neutrino oscillations is a bit different because, as soon as we prove experimentally that neutrinos are Majorana particles, we will confirm  the existence of a set of dimension-5  operators beyond the Standard Model, the so-called Weinberg operators of the form (H L)^2/Λ. Then the scale Λ is the maximum energy scale where new physics (singlet Majorana neutrinos or something more complicated) has to show up. This is however little consolation given the scale emerging from neutrino experiments is Λ∼10^15 GeV, obviously beyond the direct reach of accelerators in a foreseeable future.   

So, while pushing up the energy frontier in accelerators will continue, I think that currently searching high and low for a new scale is the top priority. Indeed, increasing the collision energy has become an expensive and time consuming endeavor; we will achieve an almost factor of 2 increase in 2 years, and, optimistically, we can hope for another factor of 2 at the time scale of ∼25 years. On the other hand, indirect sensitivity to high scales via searches for  higher dimensional operators beyond the standard model can often be improved by orders of magnitude in the near future. The hope is that Fermi's trick will work again and we may discover the new scale indirectly, by means of experiments at much lower energies. There are literally hundreds of dimension-6 operators beyond the standard model that can be searched for in experiments. For example, operators involving the Higgs fields would affect the Higgs couplings measured, and in this case the LHC and later the ILC can probe the operators suppressed by up to ∼10 TeV. Flavor and CP violating processes offer an even more sensitive probe, with the typical sensitivity between 10 and 10^5 TeV. Who knows, maybe the recent anomaly in B→K*μμ decays is not yet another false alarm, but an effect of the flavor violating dimension-6 operators of the form


with Λ of order 30 TeV.  And if not,  there are hundreds other doors to knock on.  Demonstrating the presence of a nearby new physics scale would surely bring back momentum to the particle physics program. At least, we would know where we stand, and how big a collider we must build to be guaranteed new physics.  So yes, a kingdom and on my part I'm adding the hand of a princess too..

30 comments:

wolfgang said...

>> A day may come when this blog will fall silent forever; but it is not this day...

Thank you!

Ap said...

Hi Jester,

I was getting worried that something serious had occurred so very glad to have you back. Yours is by far the best BSM blog & the field needs you!

Concerning physics, I totally agree about the need to identify a scale of new physics, but I'm not quite so pessimistic about the chance of LHC13 discoveries as a factor of 2 at this particular energy scale is still a big deal. (LHCb is a great expt but I don't at all believe the LHCb B->K*\mu\mu anomaly is new physics. Angular distributions have a long history of giving false results, and the `true' look-elsewhere correction is huge, taking it well below the 2.8 \sigma quoted.)

The silver lining of the present headless chicken situation is that there are rich opportunities for completely new non-collider experiments with associated discoveries. Given the collider timescale/cost problem that's been hanging over traditional HEP since the 1970's a movement away from big colliders might not be bad thing.

fiat lux said...

8.6 GeV FTW!

Cop Shoot Cop said...

Keep up the writing! Enjoying your blog!

Anonymous said...

Please produce a picture of the princess.

Anonymous said...

Why do you need to see a picture? You only get the hand.

Jester said...

but you can choose the left or the right hand.

johnduffieldblog said...

I wish I could get a bunch of those headless chickens in front of a whiteboard for an hour, because I think there’s just loads of new physics lying around like low-hanging fruit. But it’s in the orchard next door, in things like classical electromagnetism and TQFT and little papers that HEP guys never read. And all this new physics is within the standard model, showing why some of the beyond-the-standard-model ideas are ill-founded. I try to tell people about this “top down” stuff, but they’re just not hearing it. But there again, I suppose headless chickens aren’t too good at listening.

Robert L. Oldershaw said...


You can lead a theoretical physicist to knowledge, but you cannot make him think.

Anonymous said...

You note 4 important and promising subjects. Some are more equal than others. For those considering which to pursue, I offer some hard-earned, strongly biased opinions:

neutrino oscillations: guaranteed to be interesting

matter-antimatter asymmetry: a profound but approachable if challenging problem

cosmic inflation: a morass of theoretical nonsense

dark matter: guaranteed to frustrate and disappoint.

andrew said...

"The case of the neutrino oscillations is a bit different because, as soon as we prove experimentally that neutrinos are Majorana particles, we will confirm the existence of a set of dimension-5 operators beyond the Standard Model, the so-called Weinberg operators of the form (H L)^2/Λ. Then the scale Λ is the maximum energy scale where new physics (singlet Majorana neutrinos or something more complicated) has to show up. This is however little consolation given the scale emerging from neutrino experiments is Λ∼10^15 GeV, obviously beyond the direct reach of accelerators in a foreseeable future."

I very much doubt that neutrinos will be found to be Majorana and don't really understand why this, rather than a Dirac hypothesis, would be so attractive to theorists.

Mario said...

Hey! I guess you mean LHCb's latest paper http://arxiv.org/abs/1308.1707, not the one you mentioned. There is a deviation from form-factor invariant values. The other (you posted) is consistent with the SM.

Anonymous said...

Anon at 16.16

I also offer some hard-earned and biased opinions:

1) New results from neutrino oscillations may be experimentally interesting but they are almost entirely useless theoretically. Despite the *enormous amount of data we already have* about both lepton and quark flavor mixing and masses (for decades now) there is no good theory of why the flavor structure is what it is.
The small amount of extra data from upcoming neutrino osc expts will not help us at all. The only really useful thing will be to find out if neutrinos masses are Majorana or Dirac (as Jester correctly says). All else in the experimental direction is essentially hype about its importance. What is needed in this field is *new theoretical ideas*.

2) Dark matter (and possibly connections with matter-antimatter asymmetry) are guaranteed beyond-the-SM physics with an enormously exciting and varied experimental program that could have big impact on our understanding of the world. Saying this field is "guaranteed to frustrate and disappoint" is unthinking cynicism.

3) Given the huge amount of primordial fluctuation data which supports the basic idea of (sub-Planckian, single field) inflation this is much more likely to be true than not. Given this is one of the most profound changes in our understanding of the world that has occurred since QM it is very worth while to invest a great deal of effort in a) trying to integrate the inflationary sector into the known structure and facts of the SM, and b) collecting much more data on all length scales, eg from the future large scale structure surveys. Saying that inflation is a "morass of theoretical nonsense" shows that you fail to understand both the theory and the importance of the what we are learning from data.

Anonymous said...

You must enter the gates of Mordor to find new Physics.

Jester said...

thx Mario, link corrected

Anonymous said...

Andrew -- Without changing the standard model we can provide the neutrino a mass via Majorana terms using an effective operator LHLH/M where M is a large cut-off scale. Dirac mass requires the addition of right handed neutrinos as well as a symmetry to be imposed (lepton number symmetry). If we don't impose this additional symmetry then once again the neutrinos will have Majorana masses.

Michel Beekveld said...

Welcome back Jester.
You were missed.

Brian Wales said...

"But there again, I suppose headless chickens aren’t too good at listening."

People who get new buildings written into their contracts can't really complain about feeling like headless chickens, especially when they can't admit when they're wrong.

Loren said...

Dark matter has a chance of being identified if various in-the-works experiments and observations succeed.

If direct detection of WIMP's succeeds, we may get an interesting harvest of physics, especially if several different detector teams detect them. They use or propose to use a variety of different materials, covering the periodic table and spinning vs. spinless.

I've thought about this in detail, and one may get proton vs. neutron, spin-independent vs. spin-dependent, and even the mass of the WIMP if it's less than a few hundred GeV.

If annihilation detection succeeds, then we may get a precise WIMP mass and annihilation cross sections into both photons and neutrinos. Not quite as good, but still good.

Anonymous said...

I notice that B -> K* mu mu paper speaks only from the 1/fb worth of 7 TeV data. Any guesses on how long it will be before the 2/fb worth of 8 TeV data is crunched to shed more light on this specific subject?

Anonymous said...

Might there be some new stuff coming out of Daya Bay?

Michel Beekveld

Anonymous said...

So, I understand your point about it not being clear what scale we need to be at for direct production, but what are you experimentally suggesting? Intensity frontier experiments? Precision collider work? Something else...?

Jester said...

Suggesting? I'm just lamenting ;-)
But seriously, I think precision physics (collider or non-collider) is now the key, as we cannot start building a new high-energy machine until we're sure there's something out there to find.

Jester said...

Sure, it is possible that neutrino experiments (Daya Bay or another) will find something interesting one day.

LHCb takes its time. My guess the full statistics in B->K*mumu will be out for winter conferences.

cb said...

Instead of looking for the magic effective operator in a vast landscape randomly (Nature/God will select/choose the good one), may be courageous model-building physicists (dépités mais pas décapités/dismayed but not beheaded ;-) could use and test the hypothetical educated guess from algebraic constraints of the non-commutative geometric framework for instance? Anyway it could be that the naturalness paradigm in "standard" quantum field theory living on a Minkowski space-time is heuristically obsolete and it is required to understand better the compass role of the spin to blend somehow 4D-spacetime and internal gauge degrees of freedom before contemplating any super-space and extra-dimensions...

Anonymous said...

" Any guesses on how long it will be before the 2/fb worth of 8 TeV data is crunched to shed more light on this specific subject?"
I guess 3-8 months, depending on the interest in the LHCb group.

Chris Austin said...

What do you think of the arguments of Dicus and He, who argue in hep-ph/0409131 that by considering the onset of tree level unitarity violation in f \bar{f} -> n longitudinal W's, where f is any SM fermion, and n is typically around 10, (see the graph on page 30), the SM itself, with no assumptions about new physics, leads to the conclusion that the scale of mass generation for the SM fermions cannot be more than about 120 TeV for the charged fermions, and about 170 TeV for the neutrinos?

Stefan said...

"Ignoring gravity, the Standard Model with the 125 GeV Higgs boson can be extended to arbitrarily high scales."
<-- Do you mean with that that the current model is renormalizable? If not could you clarify that a little bit?

Jester said...

I meant just renormalizability + unitarity + vacuum stability.

Jester said...

Chris, i think this paper deal with the SM without a Higgs boson. With the 125 GeV Higgs there's no problems with unitarity of fermion scattering